"One of these [Benioff
strainmeters] in the granitic rock of the San Gabriel Mountains is
writing a continuous record of the local strain condition for eventual
correlation with the general redistribution of strain in the region
preceding and following large earthquakes. There are distant hopes that
such data may eventually lead to some form of prediction, or at least to
anticipation of the general course of seismic events in the area." (From
Charles Richter's textbook, Elementary Seismology, 1958, p. 227)

Earthquake predictability has been the subject of several recent,
controversial articles within the seismological community. The intensity
of the controversy is understandable, since it stems both from our
present inability to predict earthquakes and from the potentially great
value that prediction could have for society. Our difficulty in
predicting earthquakes is partly due to the inherent characteristics of
earthquakes and seismic waves and partly to an incomplete understanding
of the earthquake process. In order to gain some perspective on this
issue, it is useful to place the earthquake problem in the context of
other natural hazards. Nearly all other natural hazards, from hurricanes
to wildfires to volcanic eruptions, are predictable to some extent. The
predictions are based on precursors, defined here as the
non-threatening, initial phase of a natural hazard. This precursory
phase consists of two parts, the preparation of the disturbance itself
and the propagation of that disturbance to population centers. For
example, a hurricane represents an atmospheric disturbance that develops
at sea in the tropics and subsequently moves slowly toward population
centers, at which time it becomes a threat. The precursory phase,
including the preparation and propagation times, lasts hours to days.
Other weather disturbances, such as tornadoes, occur on much shorter
time scales, although the conditions under which tornadoes are highly
probable can usually be recognized. In the case of earthquakes, we have
yet to observe a reliable preparation phase, and the propagation time is
very short, on the order of seconds. Tsunamis possess much longer
propagation times, so that forecasting is possible, in the absence of an
observed preparation phase. Probably the most closely related hazard to
earthquakes is volcanic eruptions. Prediction must often be based solely
on identifying a preparation phase because in many cases the propagation
time is very short. For volcanic eruptions, however, the preparation
phase has a known physical basis, namely the pre-eruption upward
transport of magma. This magma transport has several observable
manifestations, including crustal deformation, microseismcity, changes
in the gas chemistry and increases in the temperature of hydrothermal
fluids. Volcano prediction is a reality. Perhaps the most successful
prediction was the June, 1991 eruption of Mount Pinatubo (in the
Philippines), which led to the evacuation of 80,000 people and saved
billions of dollars in U.S. aircraft that were moved from Clark Air
Force Base. This volcano had not erupted in 400 years but was
predictable from a variety of precursory signals. It is likely that
improved monitoring of crustal deformation, seismicity, and other
magma-transport indicators will ultimately lead to the routine
prediction of volcanic eruptions.

Our poor success record in earthquake prediction has understandably
produced a shift in emphasis to other aspects of natural disaster
reduction. There are clearly things that can be done to reduce the
vulnerability to an earthquake hazard, in the absence of predictive
capability, and we have made much progress in these areas. We have taken
significant steps forward both in mitigation, the long-term actions that
reduce the vulnerability to hazards, and preparedness, the short-term
actions taken around the time of an event. For example, there have been
important efforts to identify those areas that are most prone to sustaining
significant earthquake damage (through the generation of hazard maps), so
that informed decisions can be made about land use and building codes.
Warning systems that detect and immediately broadcast the occurrence of an
earthquake help with preparedness and in guiding the emergency response to
a disaster, and in special cases can give a few seconds of advanced
warning. For the other significant natural hazards, short-term forecasting
is an integral component of preparedness. With hurricanes and volcanic
eruptions, for example, buildings can be secured, equipment can be removed,
emergency services can be put on alert, and populations can be evacuated,
if necessary. It is often said in the seismological community that
earthquake forecasting would not be valuable, even if it were possible. All
we need are stronger buildings to withstand earthquakes. I believe that
this sentiment is misguided. Clearly, advanced warning has been extremely
valuable for other natural hazards, and such information in the case of
earthquakes would be equally valuable. We must ultimately admit that much
of this sentiment stems from our frustration over the surprising difficulty
of the earthquake prediction problem.

Why are earthquakes different from these other hazards? Why are earthquakes
the last of the natural hazards to be predictable? For one thing, the short
propagation time means that prediction must be based on the existence of a
preparation phase. It is clear that we have yet to detect, on a reliable
basis, such a preparation phase. Is this because there is no such phase in
the case of earthquakes, or because we have not yet observed it? This
question is at the heart of the present debate on the predictability of
earthquakes.

The notion that slow tectonic deformation might precede significant
earthquakes, and be detectable by seismic instrumentation, has been around
for decades, as illustrated by the quote from Charles Richter's 1958
textbook at the beginning of this article. This still remains, in my
opinion, the most likely form of an earthquake preparation phase. Progress,
however, has been slow in evaluating this hypothesis and more generally in
understanding the deformational context of earthquake occurrence. It is the
knowledge of this deformational environment that I believe will fill a
major gap in our understanding of earthquakes. In the broadest sense, plate
tectonic theory has provided us with the underlying cause of most
earthquakes, as due to the relative motion of plates along their
boundaries. Yet, we have only begun to explore this relationship, and the
most important questions remain unanswered. How does steady plate motion
ultimately lead to the occurrence of individual seismic events? Are there
transients in plate boundary deformation, as suggested by recent
strain/geodetic observations, and if so, what are their spatial and
temporal characteristics? Do transients propagate? How do the individual
faults within a fault system interact? How do earthquakes interact? And
finally, is there an observable preparation phase to earthquakes that may
form the basis for prediction? It is becoming increasingly apparent that
earthquakes are only the most visible part of a complex system of
interactions that we have only begun to explore. In order to more fully
understand this system that defines the plate-motion/earthquake
relationship, I believe it is necessary to characterize and understand its
most easily observable manifestation: plate-boundary deformation.

How, then, should we proceed? We can gain insight from other fields that
study complex natural phenomena. Without exception, these fields are
primarily data driven. Major advances in understanding have followed major
increases in monitoring capability. For example, recent advances in
meteorology generally, and weather forecasting particularly, were in large
part due to the deployment of a multi-billion-dollar satellite system that
allows for continuous, global monitoring of atmospheric disturbances. Our
greatest limitation in the study of plate-boundary deformation is the lack
of adequate monitoring capability. Of course, we have thousands of
seismometers that perform the important task of monitoring seismic
activity. But these are primarily intended for studying the earthquake
process itself, rather than its deformational environment.

The earthquake science community needs an adequate facility for the
semi-permanent monitoring of the plate-boundary deformation field. A plate
boundary deformation network (pbdn) ought to be established that is capable
of monitoring deformation along the roughly 1000 km by 200 km segment of
the Pacific-North American Plate boundary zone that is dominated by the San
Andreas fault system. Such a network should be capable of detecting surface
strain spanning the spatial/temporal range defined by plate motion at one
end and earthquake rupture at the other: seconds to decades and meters to
100's of kilometers. At present, there is no one seismic/geodetic technique
that covers this broad range with adequate sensitivity and dynamic range,
and at least two would be required. For example, GPS (or SAR) can cover the
long-period (one-month to decades), long-wavelength (>10km) part of this
spectrum, while point-strain measurements, such as those obtained by
borehole tensor strainmeters, could be used at shorter period (one-hour to
one-month) and wavelength, where they enjoy orders of magnitude greater
sensitivity. Seismometers can adequately cover periods shorter than one
hour. The required instrumentation has already been developed for such a
network. GPS (and SAR) technology is now standard. Also, several types of
borehole tensor strainmeters are either operational or are in final stages
of development. The pbdn should also be able to monitor strain at
seismogenic depths, as well as at the surface. This is more relevant to the
problem of earthquake occurrence, but far more difficult, because strain
cannot be measured directly. Instead, strain indicators, such as
microseismicity and temporal variations in elastic properties, must be
monitored and 'calibrated' in some way. Many of these indicators can be
observed using three-component seismometers.

The pbdn would ideally consist of 1000-2000 sites covering the plate
boundary zone at roughly 10 km spacing, and each could include, for
example, a GPS receiver, a borehole strainmeter, a borehole broadband
three-component seismometer and additionally a strong-motion accelerometer
for covering the high-frequency, high-amplitude end of deformation. It is
encouraging that the GPS/seismometer components of such a network are
presently being deployed in Southern California as part of the SCIGN
network. In order to adequately fill the sensitivity gap in the
one-hour-to-one-month period band, however, it would be necessary augment
this configuration with strainmeters. Indeed, most of the published studies
of strain transients have used data from these instruments.

The major obstacle to deploying such a monitoring network is not
technical or logistical, but insufficient resources. It is estimated
that the cost of each site would be about $100,000, including a
200-meter-deep hole for the borehole instruments, or about $100 million
for the entire network. If viewed as a 20-year experiment, with $10
million/year for maintenance and another $10 million/year for research,
this would average out to $25 million/year over the life of the
experiment. While this may sound like a large sum to many, it should be
put in perspective. As a large facility/research program in the
earthquake sciences, it would have a budget comparable to other large
programs, such as NEHRP or IRIS. The people of California could entirely
support such a program with a contribution of less than a dollar from
each resident per year!

There has been justifiable concern, which I share, that basing a major
earthquake science program solely on earthquake predictability would be
very risky, given our lack of success to date in achieving this goal. For this reason, earthquake prediction should be embedded within a rich
scientific problem that will generate significant results regardless of
whether prediction is ultimately achieved. Plate boundary deformation
constitutes such a problem. In its own right, it is an important and
relatively unexplored area of plate tectonics that is at the foundation of nearly all active tectonics. Geophysics, and particularly seismology, would play a leading role in such a broad endeavor.